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Risk Reduction or Risk Compensation? The Case of Mandatory Safety-Belt Use Laws
WILLIAM N. EVANS
Department of Economics, University of Maryland, College Park, MD 20742'
JOHN D. GRAHAM
Department of Health Policy and Management, Harvard School of Public Health, 677 Huntington Avenue, Boston, MA 02115
Abstract
The technological approach to risk regulation seeks to lessen the incidence of mortality and morbidity by modifying environmental conditions. Insofar as risk-taking behavior is purposive, social scientists have predicted that technological progress may be negated by various forms of "risk compensation." The validity of this hypothesis is tested in the transportation sector with data from the U.S. on the effects of new mandatory safety-belt-use laws. A fixed-effects model of traffic fatality counts is estimated using pooled data from 50 states during the 1975-1987 period. Results suggest that such laws have reduced mortality among car occupants to a degree that is compatible with the predictions of technologists. However, there is weak evidence of increased mortality among some nonoccupants, a pattern predicted by risk-compensation theorists. The lifesaving effects of belt-use laws are largest in states that permit primaiy police enforcement and appear to be somewhat larger for front-seat occupants age 21 and under. Although offsetting behavior appears to be small relative to lifesaving effects, it may take several more years for any compensatory behavior to achieve a new equilibrium.
Beginning with the work of Peltzman (1975), economists have become interested in potential behavioral responses to regulations designed to reduce health and safety risks. Blomquist (1988) presents a careful summary of the econometric evidence on this quesiton. Several psychologists, including Wilde (1982), have become intrigued with the same issue. The central question is whether risk-taking behavior is constant before and after installation of technological innovations designed to enhance safety. Lund and O'Neill (1986) acknowledge the possibility of risk compensation but argue that it is unlikely to occur when drivers receive no direct feedback about their enhanced safety. Evans (1985) advances the more general notion of behavioral feedback If behavior is not constant, the magnitude of offsetting (or enhancing) behavior is a critical factor in assessing the net consequences of new technology.
This research was supported in part by a grant from the Centers for Disease Control to the New England Injury Prevention Research Center. The authors thank Sam Peltzman and a referee for several helpful comments.
In this article, we explore the early American experience with mandatory seat-belt-use legislation as a natural experiment to test the risk-compensation hypothesis. Our ambition is to quantify the short-run lifesaving consequences of such legislation, taking into account any offsetting behavior.
1. American safety-belt-use laws
For years, numerous trafilic safety groups have campaigned for mandatory safety-belt-use laws. No such laws were adopted in the United States until New York became the first American state to enact a mandatory safety-belt-use law in 1984. By 1987,30 more states had passed such laws at the urging of the US. Department of Transportation (DOT) and lobbyists of automobile manufacturers. This rapid pace of legislation action reflects in part DOT'S commitment to rescind the mandatory passive-restraint standard in April 1989 if at least two thirds of the US. population became covered by strong belt-use legislation. Since this goal was not achieved, the standard has become permanent.
Since police enforcement is necessary to achieve widespread compliance with belt-use laws, it is important to note that only 9 of the 31 states allow primary police enforcement (i.e., police are permitted to apprehend and cite drivers solely for failure to wear their safety belts). The majority of states permit only secondary enforcement, which means that citizens cannot be fined for not wearing belts unless they have been apprehended by police for some other violation of the law. Table 1 contains information on the effective dates of each state law and whether or not primary police enforcement is permitted.
Roadside observational surveys of motorists have shown that belt-use legislation somewhat increases belt-usage rates. In columns 5 and 6 of table 1, usage rates are presented for states before and after the advent of belt-use laws. In all states with such laws, usage rates increased rapidly after the laws became effective, with the average increase being 28%. However, usage rates differed depending upon the type of enforcement. Using a simple average of rates across states, primary enforcement states increased usage rates by an average of 34%, while the increases in secondary enforcement states were only 25%. The immediate implication is that if belts save lives, the benefits should be observed shortly after adoption and there should be a detectable difference between primary and secondary enforcement states.
There is strong evidence that safety belts reduce an occupant's chances of being killed or seriously injured in a crash. Numerous studies concerning this question have been performed over the past 30 years. Govemment analysts, after reviewing this literature, concluded that lap/shoulder belt use in the front seat of cars could prevent 40% to 50% of fatalities to otherwise unrestrained drivers and front-right passengers (DOT, 1984). An independent analysis of real-world crash data by Leonard Evans (1986) of the General Motors Research Laboratories found that such belt systems reduce fatality risk by 40% to 45%.
On the basis ofthe belt-use and effectiveness estimates summarized above, it is possible to generate a rough estimate ofthe lifesaving effects of belt-use legislation, assuming no offsetting behavior. If belt-use rates are increased by 25 to 50 percentage points and if belts are 40% to 50% effective in preventing fatalities, then belt-use laws should produce
Table 1. American safety-belt-use laws, 1984-1987
| State | Prelaw Baseline |
Latest | |||
|---|---|---|---|---|---|
| Effective date |
Enforcement date |
Type of law^ |
Belt use'' (in%) |
Belt use (in%) |
|
| New York | 12-1-84 | 1-1-85 | P | 16 | 59 |
| New Jersey | 3-1-85 | 3-1-85 | S | 18 | 44 |
| Michigan | 7-1-85 | 7-1-85 | S | 26 | 46 |
| Illinois | 7-1-85 | 7-1-85 | s | 16 | 40 |
| Nebraska"^ | 9-1-85 | 9-1-85 | s | 23 | 45 |
| Texas | 9-1-85 | 12-1-85 | p | 13 | 61 |
| Missouri | 9-28-85 | 7-1-85 | s | 12 | 54 |
| North Carolina | 10-1-85 | 1-1-87 | p | 24 | 50 |
| Hawaii | 12-16-85 | 12-16-85 | p | 35 | 72 |
| California | 1-1-86 | 1-1-86 | s | 26 | 62 |
| Connecticut | 1-1-86 | 2-1-86 | p | 25 | 56 |
| Massachusetts'^ | 1-1-86 | 1-1-86 | s | 20 | 37 |
| New Mexico | 1-1-86 | 1-1-86 | p | 28 | 46 |
| Tennessee | 4-21-86 | 1-1-87 | s | — | 38 |
| Utah | 4-28-86 | 10-28-86 | s | 18 | 44 |
| Ohio | 5-6-86 | 7-4-86 | s | 28 | 33 |
| Washington | 6-11-86 | 1-1-87 | s | — | 53 |
| Louisiana | 7-1-86 | 8-1-86 | s | 12 | 36 |
| Idaho | 7-1-86 | 7-1-86 | s | 16 | 28 |
| Florida | 7-1-86 | 1-1-87 | s | 28 | 47 |
| Iowa | 7-1-86 | 1-1-87 | p | 27 | 55 |
| Kansas | 7-1-86 | 7-1-86 | s | 11 | 48 |
| Maryland | 7-1-86 | 7-1-86 | s | 28 | 73 |
| Minnesota | 8-1-86 | 5-1-88 | p | 20 | 47 |
| Oklahoma | 2-1-87 | 2-1-87 | s | 16 | 36 |
| Indiana | 7-1-87 | 7-1-87 | s | 10 | 44 |
| Nevada | 7-1-87 | 7-1-87 | s | 21 | 38 |
| Colorado | 7-7-87 | 7-7-87 | p | 18 | 47 |
| Montana | 10-1-87 | 1-1-88 | s | 33 | 63 |
| Pennsylvania | 11-23-87 | 3-23-88 | s | — | — |
| Wisconsin | 12-1-87 | 12-1-87 | s | 26 | 50 |
"P = primary, S = secondary.
a 10% to 25% reduction in front-seat occupant fatalities. This range presents a useful benchmark for assessing the actual fatality counts in states that have enacted such laws. Using this same type of calculation, we would expect that the 34% increase in belt use in
''The prelaw belt use numbers are taken from the last survey before use laws were enforced. Postlaw use rates are taken from the latest survey taken after the laws were enforced.
'^Massachusetts and Nebraska have since repealed their belt-use laws. The repeals became effective on 1-1-87 in both states.
Sources: The legislation dates were provided to us by Susan Partyka of NHTSA. Belt-use numbers were supplied by the National Highway Safety Administration.
primary states should produce a 15% to 17% reduction in front-seat fatalities for these states, while the 25% increase in usage in secondary states should produce a 10% to 12.5% reduction in fatalities.
2. Theoretical predictions
The offsetting behavior hypothesis implies that the effectiveness of belt-use legislation cannot be computed simply by multiplying estimated changes in belt-use rates by estimates of belt effectiveness. To accommodate this hypothesis formally, we write
$$E_{n} = f(D, B), \tag{1}$$
where £" is the net effectiveness of belt use legislation, D is the design effectiveness of legislation (as computed above), and 5 is the behavioral feedback (other than belt use) of drivers and passengers to the new legislative regime.
The implicit prediction of technologists is that B = 0 and that hence £" is determined solely by D. The risk-compensation hypothesis, in contrast, predicts that motorists will trade some or all of the enhanced protection for additional benefits of risk taking (Peltzman, 1975). Drivers, for example, may trade safety for speed in order to reduce travel time. As a result, the prediction is that B > 0 and that hence D will tend to be an overestimate of £"• An extreme case of risk compensation, called risk homeostatis by Wild (1982), is that B will always adjust such that E^ = 0. The key cognitive assumption of this psychological theory is that motorists seek a target level of fatality risk regardless of the marginal benefits and costs of risk taking. Evans (1985) has argued that plausible theories can be advanced to predict behavioral responses of any sort (even protective ones) and refers to the general phenomenon of "behaviorial feedback."
As a guide to testing these theories, it is useful to distinguish collision frequency from crash survivability. Hence we write formally
$$F = C \times \Pr(F/C) \tag{2}$$
where F is a fatality count, C is a collision count, and Pr(F/C) is the conditional probability of fatality (given a collision). The theories described above lead to some falsifiable (testable) predictions about changes in the values of F, Pr(F/C), and C. Such predictions are summarized in table 2 and form the basis of the empirical inquiry that follows. Note that if one adopts a behavioral-feedback perspective, then any values of F, Pr(F/C), and C are possible, and the exercise becomes completely descriptive.
3. Data and statistical methods
The recent movement toward mandatory belt-use laws provides natural experiments that permit analysis of the alternative behavioral hypotheses. A comprehensive analysis
| | Predicted change due to belt-use legislation | | | | | |
|----------------------------|----------------------------------------------|----------|----------|--|--|--|
| Theoretical
perspective | C | Pr(F/C) | F | | | |
| Technologist | 0 | Decrease | Decrease | | | |
| Risk compensation | Increase | Decrease | 7 | | | |
| Risk homeostasis | Increase | Decrease | 0 | | | |
| Behavioral feedback | 7 | 9 | 7 | | | |
Table 2. Summary of theoretical predictions
would incorporate all information over the time period (i.e., both states that have laws and those that do not). Hence, we pooled time series data for all 50 states. The interstate and intertemporal variations in the variables of interest (F, C, and Pr(F/C) are examined with a fixed-effects specification. In this section we first describe the choice of an outcome measure, and then the statistical model.
Information on traffic fatalities for the 1975-1987 period was obtained from the National Highway Traffic Safety Administration's Fatal Accident Reporting System (FARS). FARS is a complete census of traffic fatalities in the United States, and thus there are no sampling issues. Fatality counts in passenger cars were aggregated at the state level by year, by seating position (front versus rear seat), and by age of the victim (21 years of age and under versus over age 21). Unfortunately, no national data system exists for nonfatal injuries or collisions that do not produce injuries. As a proxy for collision counts, FARS counts of pedestrian, motorcycle, and bicycle fatalities were obtained by state and year. These are the same proxies employed by Peltzman (1975) in his analysis of the 1966 safety legislation.
Let Fit represent the natural logarithm of front-seat car-occupant fatalities for state s in year t. The log fatalities are assumed to be generated through the equation
$$F{st} = \mathbf{X}'{st} \,\mathbf{\beta} + \tau_s + \nut + \epsilon{st} \tag{3}$$
where Xj( represents a vector of characteristics for state s in year ?, p is a parameter vector, T^ and V( are state and year effects, respectively, and ej, is a zero mean random error. The state effects capture the omitted determinants of fatalities that are constant over time, but vary across states (such as road conditions and health care delivery systems), while the time effects measure the omitted determinants of fatalities that vary over time, but are constant across states (such as fuel prices and advances in automobile safety technology). The semilog form was chosen because we expect laws of equal stringency to reduce deaths by the same percentage. In this analysis, we assume that the state and year effects are fixed and that therefore they can be estimated by inserting a series of state and time dummy variables in equation (3).
Since we employ a fixed-effects specification, the estimate of p attributes only those effects that cause a state's log fatality count to deviate from the time and state means as measured by T^ and v,. The elements of the vector Xj, will be those characteristics that alter the number of collisions (C) or the conditional probability of a fatality given a collision (Pr(F/C)). Since many of the state characteristics that determine C or Pr(F/C)
are slow-moving over time, most of the state-by-state variation in log fatalities will be captured by the fixed effects. The fixed-effects model is a convenient specification, since we do not need to explain the causes of permanent interstate differences in the log fatality rates, and therefore we include in X^, only those variables that may change rapidly within the time frame of our analysis.
In order to control for exposure to traffic collisions, two types of data were collected. The Federal Highway Administration reports estimates of vehicle miles of travel (rural, urban, and total) by state and year. Since the business cycle is known to influence exposure to collisions (beyond its direct influence on total miles of travel), unemployment rates were also collected by state and year. In an earlier paper, Evans and Graham (1988) demonstrated that business cycle indicators should be incorporated into retrospective statistical evaluations of traffic safety policies.
One element of X^, will be a measure of the belt usage attributable to use laws. Ideally, we would like to have included belt-use rates as an element of the X^, vector. However, reliable measures of usage were not available for most states, especially in states that have not adopted belt-use laws. If we assume that each state has a stationary level of belt use in the absence of use legislation, a dummy variable will capture usage attributable to legislation. The variable SEATBELTj, is a dummy variable equaling 1 if state s has adopted any form of mandatory belt-use law in t, and zero otherwise. To capture the differences in usage rates across types of enforcement, we included separate dummy variables for PRIMARY and SECONDARY enforcement states. Note that the dummy variables for legislation are based on the law's effective date, not its enactment date. If a law took effect in the middle of a year, the value of the legal variable for the year was set equal to the fraction of months in that year that the law was in effect.
Given the above discussion, the equations we will estimate are of the following form:
Model 1: F,, = p, Ln (MILES TRAVELED),, + P2 UNEMPLOYMENT^,
+ 33 SEATBELT^, -I- T^ + v, + e^.
Model 2: F,, = pi Ln (MILES TRAVELED)^, + ^2 UNEMPLOYMENT,,
+ P3 PRIMARY,, -I- P4 SECONDARY,, + T^ + v, + e,.
where Fst is the log of the particular fatality variable.
Variable definitions and descriptive statistics for the variables are presented in table 3. Given the sample period, an average of 22,800 front-seat occupant fatalities occur per year, of which 27% are 21 years of age or under. There are approximately 7400 pedestrian, 4350 motorcyclist, and 915 bicyclist fatalities per year. Copies of the original data and relevant programs are available from the authors upon request.
To facilitate specification tests of the model, state and year means were subtracted from, and sample means were added to, each variable before regressions were run. These transformations eliminate the need to estimate T, and v, for each state and year, respectively (see Judge et al., 1980, pp. 340-341). One drawback of these transformations is that since much of the covariance has been eliminated from the data by subtracting means, the R^ will appear deceptively low in comparison with the more traditional
Table 3. Variable definitions and descriptive statistics
| Name | Variable definition | Mean (std.dev.) |
|---|---|---|
| CAR-OCCUPANT | Front-seat car-occupant fatalities | 455.5 |
| FATALS | (428.4) | |
| CAR-OCCUPANT | Front-seat car-occupant fatalities | 324.4 |
| FATALS > 21 | greater than 21 years of age | (314.0) |
| CAR-OCCUPANT | Front-seat car-occupant fatalities | 131.1 |
| FATALS < 21 | less than or equal to 21 years of age | (118.4) |
| PEDESTRIAN | Pedestrian fatalities | 147.2 |
| FATALS | (178.4) | |
| MOTORCYCLIST | Motorcyclist fatalities | 86.9 |
| FATALS | (116.1) | |
| BICYCLIST | Bicyclist fatalities | 18.3 |
| FATALS | (22.8) | |
| MILES | Vehicle miles of travel, x 100 million | 32023.7 |
| TRAVELED | (32528.6) | |
| UNEMPLOYMENT | Unemployment rate, in percent | 7.16 |
| (2.25) | ||
| SEATBELT | Seatbelt dummy variable, = 1 if state | 0.060 |
| has mandatory seatbelt law, 0 otherwise | ||
| PRIMARY | Enforcement dummyvariable, = 1 if | 0.021 |
| mandatory seatbelt law permits | ||
| primary police enforcement, 0 otherwise | ||
| SECONDARY | Enforcement dummy variable, = 1 if | 0.039 |
| mandatory seatbelt law permits only | ||
| secondary police enforcement, 0 otherwise | ||
| N | Number of observations | 650 |
dummy-variable specification of fixed-effects models. However, the parameter estimates and standard errors for both specifications are arithmetically equivalent.
Because there is a wide variance in the number of fatalities across states, the additive error e,, may not be identically distributed. To correct for the possible inconsistency in the standard errors attributable to heteroskedasticity, standard errors are reported according to the method proposed by White (1981).
4. Results
Before presenting results of the fixed-effects model, we offer a more intuitive statistical assessment of the effects of the laws. Fatality rates (per vehicle mile of travel) were computed for each state for the years 1984,1985,1986, and 1987. The fatality rates for each of the 16 states that enacted belt-use laws before 1987 were deflated by the average fatality rate for the remaining states that did not enact belt-use laws during this period, in order to control for factors other than the laws. (Nebraska and Massachusetts were excluded because they adopted and then repealed their laws in this same period.) We then calculated the percentage change in this ratio between the year prior to and the first full year after the adoption of a belt-use law. For example, since Michigan's belt-use law became effective in July of 1985, we compared the percentage change in the 1984 and 1986 ratios. This percentage change can be considered a crude measure of the effect of the law.
Table 4 presents the computed percentage changes for all states with belt laws, for primary enforcement states only, and for secondary states only. Fatalities to front-seat car occupants, to pedestrians, to motorcyclists, and to bicyclists are analyzed separately. This rather simple statistical approach suggests that belt laws are associated with a decline in the car-occupant fatality rate. The average percentage decline in the caroccupant fatality rate is larger for the five states that permit primary police enforcements than it is for the 11 states that permit only secondary police enforcement ( - 20.6% vs. - 6.6%). There is no clear association between belt laws and pedestrian fatality rates. In the case of bicyclists, fatalities in primary and secondary states increased by 35% and 12%, respectively. This large increase in fatalities for bicyclists in primary states is due in part to the fourfold increase in fatalities in Connecticut between 1985 and 1987, where bicycle fatalities increased from 3 to 12.
The fixed-effects model that we have proposed permits a more rigorous statistical analysis of these effects. Estimates of regression equations for car occupants and nonoccupants are reported in tables 5 and 6. As expected, fatality counts are positively associated both with miles of travel and with the business cycle (measured as unemployment).
In the car-occupant regressions, the estimated coefficients for the seat-belt-law variables exhibit a negative sign, as technologists would predict. The estimated coefficient suggests that, on average, enactment of belt-use laws is associated with an 8% decline in front-seat occupant fatalities. The lifesaving effect appears to be relatively larger in percentage terms for occupants 21 years of age or under (although the standard errors are large enough to suggest no difference). When separate dummy variables are added
Table 4. Average percentage change in selected fatality rates following passage of belt-use laws
| | Average percentage change in state
fatality rates in first full year
after enforcement of belt-use law^ | | | | |
|---------------------|---------------------------------------------------------------------------------------------------------------|------------------------------------------------------|--|--|--|
| Fatality categories | States allowing
only secondary
enforcement (N
= 11) | States permitting
primary enforcement (A/
= 5) | | | |
| Car occupants | -7.0 | -20.8 | | | |
| < Age 21 | -3.1 | -23.6 | | | |
| > Age 21 | -8.1 | -20.1 | | | |
| Pedestrians | + 7.4 | -4.6 | | | |
| Motorcyclists | + 5.8 | -2.0 | | | |
| Bicyclists | + 12.2 | + 35.0 | | | |
"Average fatality rates in belt-law states deflated by average fatality rates in remaining states without belt-use laws; percentage change is calculated for either 1984 vs. 1986 or 1985 vs. 1987, depending upon when the state law took effect.
Table 5. Fixed-effeet results, car-occupant fatalities: parameter estimates, and heteroskedastic-consistent standard errors
| Ln (CAR-OCCUPANT FATALS) |
Ln (CAR-OCCUPANT FATALS > 21) |
Ln (CAR-OCCUPANT FATALS < 21) |
||||
|---|---|---|---|---|---|---|
| Independent variable |
(1) | (2) | (1) | (2) | (1) | (2) |
| Ln (MILES | 0.397 | 0.434 | 0.352 | 0.382 | 0.427 | 0.484 |
| TRAVELED) | (0.105) | (0.104) | (0.112) | (0.112) | (0.137) | (0.132) |
| UNEMPLOYMENT | -0.025 | -0.024 | -0.029 | -0.029 | -0.014 | -0.013 |
| (0.004) | (0.004) | (0.004) | (0.004) | (0.006) | (0.006) | |
| SEATBELT | -0.084 | - | -0.085 | — | -0.110 | — |
| (0.036) | (0.035) | (0.049) | ||||
| SECONDARY | - | -0.031 | — | -0.041 | — | -0.049 |
| (0.037) | (0.035) | (0.049) | ||||
| PRIMARY | - | -0.170 | — | -0.154 | — | -0.243 |
| (0.053) | (0.051) | (0.079) | ||||
| 0.11 | 0.12 | 0.13 | 0.13 | 0.04 | 0.05 |
Table 6. Fixed-effect results, nonoccupant fatalities: parameter estimates and heteroskedastie-consistent standard errors
| Ln (MOTORCYCLIST FATALS) |
Ln (PEDESTRIAN FATALS) |
Ln (BICYCLIST FATALS) |
||||
|---|---|---|---|---|---|---|
| Independent variable |
(1) | (2) | (1) | (2) | (1) | (2) |
| Ln (MILES | 0.279 | 0.258 | 0.943 | 0.951 | 0.837 | 0.855 |
| TRAVELED | (0.174) | (0.175) | (0.142) | (0.145) | (0.249) | (0.255) |
| UNEMPLOYMENT | -0.025 | -0.025 | -0.026 | -0.025 | -0.012 | -0.012 |
| (0.008) | (0.008) | (0.006) | (0.006) | (0.010) | (0.010) | |
| SEATBELT | 0.034 | — | 0.087 | — | 0.143 | — |
| (0.059) | (0.036) | (0.070) | ||||
| SECONDARY | — | 0.007 | — | 0.103 | — | 0.168 |
| (0.066) | (0.044) | (0.076) | ||||
| PRIMARY | — | 0.080 | — | 0.061 | — | 0.103 |
| (0.061) | (0.040) | (0.108) | ||||
| 0.02 | 0.02 | 0.13 | 0.13 | 0.10 | 0.10 |
for primary and secondary laws, only the primary law variable has a statistically significant coefficient. The estimated coefficients suggest that primary laws produce a 17% reduction in fatalities, while secondary laws produce about a 3% decline. Once again, the lifesaving effects appear to be larger for car occupants 21 years of age or under. For all three fatality categories, we reject the hypothesis that the lifesaving benefit of belt-use laws is the same in primary and secondary enforcement states.
The results in table 6 for nonoccupants provide suggestive evidence for the offsetting behavior hypothesis. The legal variables are positively associated with all three nonoccupant fatality categories (populations that are not protected by restraint systems), although the standard errors for many of the variables tend to be quite large relative to the estimated coefficients. The absolute sizes ofthe coefficients are larger for secondary than primary laws in the motorcycle and bicycle regressions, a pattern that is not predicted by the risk-compensation hypothesis. There is no evidence in these results to support the more extreme risk-homeostasis theory. At a minimum, the somewhat ambiguous results for nonoccupants lend credence to our inference that it was indeed belt laws that produced the decline in front-seat car-occupant fatalities.
Although the first state law did not become effective until 1985, we chose to extend the panel for each state until 1975, the first year available on the FARS tape. Given our fixed-effects specification, a longer panel will provide better estimates of the state effects. The results, however, were found to be relatively insensitive to the length of the series.
An alternative method for estimating equation (3) would be the random-effects specification, where T^ and v, are considered draws from a normal distribution with zero mean and finite variance. The implication of the random-effects assumption is that the state and year effects must be orthogonal to the elements of X^,, whereas the fixed-effects model allows for correlation between these variables. For panels that are large in the time dimension, random and fixed effects will be asymptotically equivalent. However, for finite samples, care must be taken when choosing a model. If the random-effects specification is correct, use of the fixed-effects model will result in a loss of efficiency; where the fixed-effects model is true and a random-effects model is used, parameter estimates will be biased.
We would expect that the amount of driving in a state, as measured by vehicle miles of travel, should be correlated with not only the intertemporal movements in a state's fatalities, but also interstate movements in the mean level of fatalities. As a result, our prior belief is that the fixed-effects specification is the more appropriate model. To test the specification, we performed a Hausman (1978) test with the null hypothesis being no difference in the fixed- and random-effects estimates of p. The random-effects model was estimated according to the procedure of Fuller and Battese (1974). For model 2 of the front-seat car-occupant fatalities equation, the Hausman test statistic is 17.42, which is distributed as a chi-square with four degrees of freedom. We reject the hypothesis that the two procedures are equivalent, which suggests that the state and year effects may not be orthogonal to the other right-hand-side variables.
Although the test statistic suggests that the random and fixed effects are different across all regressions, the results for the business cycle and for the legal variables are similar under both procedures. The random-effects parameter estimates (standard errors) for model 2 of the front-seat car-occupant equation are as follows: Ln(MILES TRAVELED) = 0.93 (0.03), UNEMPLOYMENT = -1.7E-2(4.1E-2), SECOND-ARY = -0.06(0.04), PRIMARY = -0.22(0.05). The failure of the Hausman test is due primarily to the size and the precision of the Ln(MILES TRAVELED) variable in the random-effects specification. The PRIMARY coefficient is larger in the randomeffects model, while the coefficient for the SECONDARY variable is of roughly the same magnitude but still statistically indistinguishable from zero. In the nonoccupant fatality equations, belt-use laws had a small positive but statistically insignificant effect on fatalities.
5. Discussion
The results of this study provide some evidence of a substantial short-term benefit from mandatory belt-use laws, especially in primary enforcement states. Reviewing the predictions of the alternate hypotheses in table 2, the results for primary enforcement states support the predictions of technologists, while the risk-homeostasis hypothesis is rejected. There is some evidence that belt-use laws have generated an increased number of collisions as measured by pedestrian, motorcyclist, and bicyclist fatality counts. However, these results are statistically significant only for secondary enforcement states.
The lifesaving benefits of mandatory belt-use laws estimated in this research are at least as large as those reported in other recent reports. Wagenaar et al. (1987), Partyka (1987), and Campbell et al. (1986) find, using quite different statistical methods, that front-seat occupant fatalities were reduced roughly 5% to 8% in the first eight states to require belt use. However, these studies do not differentiate lifesaving effects by enforcement type. In contrast, our resuhs for primary states are not as large as those of Latimer and Lave (1987), who find that in New York (a primary enforcement state), belt-use legislation reduced front-seat occupant fatalities by 25%.
Comparing the results in table 5 with the benchmark predictions at the end of section 1, we find that the estimated 17% decline in fatalities in primary enforcement states conforms with these predictions, while the estimated 3% drop in fatalities for secondary states is substantially smaller than the predictions. This modest effect in secondary states may be attributable to the demographic characteristics of those who use belts. Groups that pose the greatest risks (male teenagers and drunk drivers, for example) are also the least likely to buckle up (Evans et al., 1982; Evans and Wasielewski, 1983). Consequently, the lifesaving potential in secondary states may be limited because only the safest drivers are actually buckling up.
To estimate the number of lives saved due to legislation-induced increases in belt use, we performed a simple simulation. Using the results from model 2 of the front-seat occupant regressions, we calculated that in the eight primary enforcement states for the years 1985-1987, a total of 1635 lives were saved by increased belt use. (The standard error of this estimate is 412.8.) We also estimated the increase in nonoccupant fatalities (pedestrians -I- motorcyclists -I- bicyclists) that occurred in primary and secondary enforcement states. The estimated fatality increases and the associated standard errors are 373 (327) and 724 (443) for primary and secondary states, respectively. These results suggest that the modest lifesaving benefits in secondary states are completely offset by possible increases in nonoccupant deaths in these states. However, the estimated number of lives saved and lost have very large standard errors. In contrast, the estimated number of lives lost due to nonoccupant collisions in primary states is swamped by the lifesaving effects for occupants.
Although secondary enforcement does appear to increase belt use (see table 1), our results suggest that there may be little lifesaving benefit in those states. Our estimates indicate that in the secondary enforcement states over the period 1985-1987, a total of 558 lives were saved by belt-use laws, but the standard error of this estimate is 624.5.
It is important to emphasize that the results presented in this article relate only to the short-term effects of safety-belt-use legislation. If compensatory behavior is not immediate, long-term effects will differ from short-term effects. We concur with Peltzman (1977) that it may take several years for compensatory effects to play themselves out (Graham and Lee, 1986). Likewise, citizen compliance with legislation may either increase or erode over time. Hence, further research on the long-run effects of these laws is appropriate.
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